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Under review as a conference paper at ICLR 2027

When AI Reviews Its Own Code: Recursive Self-Training Collapse in Code LLMs

Abstract

Recursive self-training can degrade neural generative models when generated data is reused without fresh human data or external quality control. We study this risk in code LLMs, where AI-generated code can enter real repositories, later become training data, and create a repository-scale self-training loop. While software development traditionally interrupts this loop through pull-request review, tests, compilation, and human approval, AI coding tools now produce code faster than humans can review it, and code review itself is increasingly automated by AI systems. We therefore compare three recursive fine-tuning regimes: no review, human-style exogenous-gate review using model-independent filters such as compilation and static quality checks, and AI-self-gate review using the code LLM's own signals such as perplexity and binary self-scoring. Across multiple code LLMs and benchmarks, every tested recursive regime falls below its own starting point; exogenous filters preserve executable validity and sometimes reduce decline, while AI-self-gate filters can look strong early but later lose their filtering effect. In the clearest case, the binary self-gate enters a rubber-stamp regime where acceptance scores rise while benchmark correctness falls. We explain this behavior by formulating review as gated distributional reweighting, proving that AI self-gating degenerates to ungated self-training under a self-confirming acceptance condition, and giving a spectral analysis of representation-level covariance concentration under recursive retraining. These results suggest that stable recursive code LLM training requires exogenous verification rather than model-coupled self-review.

Primary area:
foundation or frontier models, including LLMs
Keywords:
code language models, recursive self-training, model collapse, synthetic code, self-review, quality filtering, generator-reviewer coupling

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_sD9BOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper investigates recursive self-training of code large language models (LLMs) under different filtering conditions, ranging from no filtering to fixed exogenous filtering and model-coupled filtering. Through experiments covering four model families and multiple benchmarks, the authors compare compilation checks, static quality rules, perplexity-based filtering, and binary self-scoring. The results show that all evaluated approaches lead to a decline in model performance. The paper further explores the impact of coupling between the evaluator and the generator and provides a theoretical analysis of gated training and representation-level covariance concentration.

Critical strengths
  • The paper addresses a practically significant question: when a continuously evolving model is used both to generate code and to filter data for its own subsequent training, can the filtering process still provide a reliable quality signal?

  • The experiments span four families of code-generation models and multiple execution-based benchmarks. The round-by-round results demonstrate that, under the recursive training protocols used, these filtering rules fail to maintain the models’ initial performance levels.

Critical weaknesses
  • There are mathematical errors in the spectral analysis presented in the main text. Proposition 2.1 incorrectly calculates repeated covariance updates by taking powers of the singular values of a general matrix AA, and it incorrectly derives an exact limit from a lower bound. Appendix E and Section F.3 provide a revised result that requires AA to be a symmetric positive-semidefinite matrix and assumes the initial covariance is diagonal in the same eigenbasis, but the proposition in the main text omits these restrictions. The authors should revise the proposition and its proof and adjust the theoretical conclusions accordingly.

  • The experimental design fails to isolate the impact of coupling between the evaluator and the generator. Compile, Quality, and AI self-gates differ in both their acceptance criteria and whether the evaluator evolves alongside the generator. Therefore, the observed performance differences cannot be attributed solely to the exogeneity of the filtering process. The authors should compare frozen and updated versions of the same evaluator using the same scoring rule and matched sampling and training budgets. Furthermore, the claim that “stable recursive training requires external verification” should be qualified.

Questions for authors
  • The claim that compilation checks prevent the spread of runtime errors lacks sufficient support from the execution-based analysis. In Table 8, the 89.4% relaxed pass rate for Compile R10 includes 78.0% ImportError cases, while the strict pass rate is only 11.4%. Failed imports leave subsequent code untested. Could the authors address these dependency issues or label these samples as execution-unresolved, and base claims about executable validity on completed execution results?

  • The experiments do not distinguish between the effects of recursive feedback and those of continued fine-tuning. In Table 13, MBPP+ performance for Qwen2.5-Coder under the Compile condition drops from 0.582 to 0.045 in the first round before recovering to 0.127 by Round 5. Could the authors include a control experiment using a frozen initial generator to produce fresh samples, while keeping the filtering criteria and training budget constant, to isolate the additional effect of recursive feedback?

  • Key training details remain incomplete. Appendix N primarily covers generation batches and hardware. Could the authors provide the full training configuration and the actual amount of data used?

  • There is an inconsistency between the described PPL filtering criteria and the reported pass rates. The main text and Appendix H.1 state that the 25% of candidates with the lowest perplexity are retained from a pool of 20,000. However, Table 9 shows pass rates varying from 0.167 to 0.235. Additionally, Figure 4 depicts both Compile and Quality pass rates as 1.0, whereas Table 3 reports a raw gate pass rate of 0.898 for Compile. Could the authors clarify the denominators used for these metrics, the stages at which they are calculated, and whether any additional filtering steps are applied, and ensure that these descriptions are consistent throughout the paper?

  • An increase in pass rates or scores is not, by itself, sufficient evidence that filtering capability has degraded. The experiments retain the top 25% of samples based on their scores. The effectiveness of this approach depends on whether the ranking distinguishes between correct and incorrect code. However, Theorem 2.3 assumes that the acceptance function is constant on the support of the generator’s distribution. Could the authors clarify the connection between this assumption and the actual ranking-based filtering process, and provide details on the relationship between filtering scores and code correctness?

  • Table 2 states that the best-performing AI self-gate is selected based on Round 5 HumanEval+ results. For Code Llama, PPL was selected with a score of 0.134. Yet in Table 14, the corresponding score for Binary is 0.1585, which is higher. Could the authors explain this selection and verify the associated summaries and comparisons?

  • Appendix C.3 discusses additional runs, but Table 7 is labeled as “single-seed,” and the six sets of HumanEval and MBPP results match the corresponding Round 5 results in Tables 11 and 13. Are these results derived from independent runs? Could the authors report variability across repeated training runs to better support comparisons between different filtering strategies?

  • The layout and clarity of the figures and tables require improvement. On page 8, Figure 2 obscures the final row of Table 2. The double horizontal lines and spacing in Table 1 could be simplified, and the small text and formulas in Figure 1 should be made more legible. Please adjust the figure and table layouts, standardize the table formatting, and improve the readability of the labels in Figure 1.

4 comments
AuthorsOpenReview ↗

rebuttal to Reviewer sD9B

Thank you for the detailed review. Our implementation is open source under MIT.

1. Weakness 1. Spectral assumptions.

Proposition E.1 and §F.3 establish spectral concentration under a symmetric positive-semidefinite update, a strict leading eigenvalue gap, and a shared covariance eigenbasis with positive leading variance. We will make these assumptions explicit in §2.2. This provides a rigorous theoretical basis for representation concentration under repeated updates.

2. Weakness 2. Reviewer coupling.

Our experiments provide both policy-level and controlled comparisons. Paper Table 1 and §3.2 compare complete training policies across five rounds. Rebuttal Table R1 (YWuj, Question 2) directly compares frozen and current reviewers using identical candidates, scoring rules, and selection quotas. At R5, frozen reviewers achieve higher AUROC and selection lift for both Binary and PPL. These matched results show that reviewer updates reduce filtering effectiveness, supporting our analysis of reviewer coupling.

3. Question 1. Import failures.

We distinguish dependency failures from successful execution. Paper Table 8 reports the original environment, while Table R4 adds strict execution results with pinned dependencies and a five-second timeout. Compile consistently achieves higher strict completion than Vanilla. At R5, Compile reaches 17.2% versus 9.4% for Vanilla, showing that compilation-based filtering improves execution reliability even under strict evaluation.

Rebuttal Table R4. Strict execution in the original and pinned environments

SettingGateRound rrStrict completion (%)Failure categoryFailure rate (%)
Paper Table 8Vanilla16.2Import failure49.2
Paper Table 8Compile112.0Import failure76.2
Paper Table 8Vanilla54.0Import failure30.6
Paper Table 8Compile1011.4Import failure78.0
PinnedVanilla112.8Unresolved dependency35.4
PinnedCompile119.6Unresolved dependency54.8
PinnedVanilla59.4Unresolved dependency19.8
PinnedCompile517.2Unresolved dependency49.6
PinnedCompile1020.8Unresolved dependency55.2

Both rates use all samples as the denominator. Paper Table 3 separately reports raw gate acceptance and accepted-set execution.

4. Question 2. Frozen generator.

Our design separates the initial fine-tuning effect from later recursive feedback. A frozen R0 generator producing fresh samples under the same Compile gate and training budget provides a direct control for recursive generation. Paper Table 13 (Rebuttal Table R2, VBf1) shows that the R1 decline occurs before any updated generator produces training data. Later rounds track the effect of repeatedly using updated models to generate training samples. This distinction allows us to examine initial training effects and recursive feedback separately.

5. Question 3. Training and data volume.

Our experiments follow a consistent training setup across models and gates. §3.1 and Appendices I and N specify five rounds with 3,000 updates per round. Vanilla, Compile, Quality, and Binary each retain 25,000 rows per run. PPL retains 21,046 for SantaCoder, 23,637 for StarCoder2, 20,221 for Qwen, and 24,104 for Code Llama. We use The Stack Dedup Python, 1,024-token prefixes and generation cap, temperature 0.8, top-p 0.95, 2,048-token packing, effective batch 64, peak LR 5×10−55\times10^{-5}, cosine decay, weight decay 0.05, and 500 R1 warmup steps. No generations or benchmark tasks were cherry-picked. We will release exact settings, prompt IDs, seeds, revisions, sample counts, hashes, and logs for full reproducibility.

6. Question 4. Pass-rate denominators.

The reported rates measure different stages and are consistent. The legacy PPL selector retains the lowest 25% of finite scores, giving 3,347 and 4,698 accepted samples out of 20,000 candidates at R1 and R5 for SantaCoder (Paper Table 9). The current selector targets 5,000 when enough finite scores are available. Paper Figure 4 measures execution among 5,000 accepted samples, while Table 3 measures raw acceptance (5,000/5,568 = 89.8%). Quality also limits repeated nonempty lines to 30% and requires at least 50 completion tokens. We will clarify these denominators.

7. Question 5. Constant acceptance versus ranking.

Theorem 2.3 establishes when self-gating loses its filtering benefit under candidate-independent acceptance. Our experiments provide direct evidence of declining ranking quality under fixed selection quotas. Table R1 (YWuj, Question 2) shows that current reviewers have lower AUROC and selection lift than frozen reviewers at R3 and R5 on identical candidates. This directly supports our finding that reviewer updates weaken code selection, beyond changes in scores alone.

AuthorsOpenReview ↗

rebuttal to Reviewer sD9B

8. Question 6. Code Llama summary row.

Paper Table 14 confirms that Binary achieves the highest R5 HumanEval+ score among AI-based gates (0.1585), exceeding PPL (0.1341). Compile remains the strongest overall at 0.1707. We will correct Paper Table 2 to reflect these results. This correction does not change our main findings or conclusions.

Rebuttal Table R5. Code Llama-7B R5 pass@1 for the Paper Table 2 correction

GateHumanEvalHumanEval+MBPPMBPP+LiveCodeBench
Compile0.18900.17070.12430.08990.003
PPL0.16460.13410.20630.17460.000
Binary0.18290.15850.16670.14810.003

9. Question 7. Independence and variability.

Paper Table 7 summarizes the same single-seed runs reported in Tables 11 and 13, rather than independent repetitions. We will clarify this in Appendix C.3. Importantly, our findings are supported by comparisons across four code LLM families, multiple benchmarks, five selection strategies, and five training rounds. These results provide broad evidence of recursive self-training degradation across different experimental settings.

10. Question 8. Layout.

We will improve the presentation by separating Paper Figure 2 from Table 2, simplifying the rules in Table 1, and enlarging the labels and equations in Figure 1. These changes will make the experimental results and theoretical analysis easier to follow.

As the rebuttal period ends tomorrow, please let us know if you have any remaining concerns. We would be grateful if you could revisit your assessment in light of our rebuttal and additional experiments. Thank you again for your review and consideration!

We sincerely appreciate your time and thoughtful feedback. We hope you will carefully reconsider our contributions and the additional evidence provided. Our code is open-source under the MIT license to support reproducibility and future research. We would be truly grateful if you could revisit your assessment and consider raising your score.

Reviewer_VBf1OpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper investigates recursive self-training collapse in code large language models (LLMs), focusing on the effects of different code review mechanisms. The authors compare three training regimes: no review, exogenous review using model-independent quality filters, and AI self-review using model-derived signals such as perplexity and binary self-scoring. Experiments are conducted on four code LLMs, including SantaCoder, StarCoder2, Qwen2.5-Coder, and Code Llama, using HumanEval+, MBPP+, and other benchmarks. The results indicate that all evaluated recursive training regimes lead to performance degradation relative to the original models. While exogenous filters can improve certain measures of code validity, AI self-review may gradually lose its ability to distinguish high-quality from low-quality samples.

Critical strengths
  • The problem investigated has significant practical implications.
Critical weaknesses
  • Although the research problem is meaningful, the technical novelty of the proposed approach is limited. Recursive model collapse caused by training on self-generated data has already been extensively investigated[1-5]. Therefore, the central ingredients of the proposed framework are largely established. The main incremental contribution appears to be an empirical comparison of filtering strategies over multiple recursive training rounds. While this comparison may be valuable, the paper does not sufficiently establish how its methodological or theoretical contributions fundamentally advance beyond existing research.

[1] Chasing Shadows: Pitfalls in LLM Security Research, Evertz et al., NDSS 2026

[2] AI Models Collapse When Trained on Recursively Generated Data. Shumailov et al. , Nature 2024

[3] Self-Consuming Generative Models with Curated Data Provably Optimize Human Preferences Ferbach et al. · NeurIPS 2024

[4] Self-Improvement Can Self-Regress: The Rise-and-Collapse Failure Mode of LLM Self-Training, Jianzhe Lin

[5] Learning to Solve and Verify: A Self-Play Framework for Code and Test Generation, Zi Lin et al.

  • The theoretical analysis of spectral concentration in Proposition 2.1 contains mathematical errors. In Section 2.2, the authors consider the covariance recursion Σₜ₊₁ = AΣₜAᵀ and use the singular value decomposition of A to derive the evolution of its covariance spectrum. However, for a general matrix A = U diag(sᵢ)Vᵀ, it is not valid to conclude that Aᵗ = U diag(sᵢᵗ)Vᵀ. Consequently, the expression for Σₜ in Proposition 2.1 does not hold for general matrices under the stated assumptions. Moreover, the asymptotic eigenvalue-ratio conclusion can be disproved by a simple counterexample. Consider A = diag(1, 1/2) and Σ₀ = I, which satisfy the assumptions of Proposition 2.1. The covariance recursion yields Σₜ = diag(1, 4⁻ᵗ), and therefore λ₁(Σₜ)/λ₂(Σₜ) = 4ᵗ → ∞. However, the proposition states that this ratio converges to the finite value α/λ₂(Σ̃₀) when λ₂(Σ̃₀) is positive.

  • The experiments do not sufficiently establish that the observed performance degradation is caused by recursive model collapse rather than other training effects. The authors compare recursively fine-tuned models against their original pretrained baselines. However, substantial performance degradation occurs immediately after the first fine-tuning round. For example, the MBPP+ performance of Qwen2.5-Coder-1.5B decreases from 0.582 to 0.045 after only one round under Compile filtering. Such a large initial degradation raises the possibility that the observed performance loss is partly caused by catastrophic forgetting, distribution shifts between pretraining and fine-tuning data, or inappropriate fine-tuning configurations, rather than the recursive accumulation of model-generated errors.

Questions for authors

Q1: How can the authors distinguish performance degradation caused by recursive self-training collapse from other effects, such as catastrophic forgetting or fine-tuning-induced distribution shifts?

3 comments
AuthorsOpenReview ↗

rebuttal to Reviewer VBf1

Thank you for the related-work suggestions and the opportunity to clarify our contributions.

1. Weakness 1. Novelty.

Our work goes beyond existing studies of model collapse [2], data curation [3], recursive code generation [1], self-training failures [4], and solver-verifier training [5]. We systematically compare fixed verification gates with evolving self-review gates across multiple code LLMs and training rounds. Theorem 2.3 explains when self-gating loses its filtering benefit, while Paper Table 2 shows how different gates affect long-term code correctness. Our main contribution is identifying and analyzing the role of code selection in recursive self-training.

2. Weakness 2. SVD powers and finite limit.

Proposition E.1 and §F.3 establish spectral concentration under explicit assumptions: a symmetric positive-semidefinite update, a strict leading eigenvalue gap, and a shared covariance eigenbasis. We will use this corrected proof in §2.2. Importantly, our main analysis of self-gating in §2.3 is independent of this result and follows directly from conditioning on acceptance.

3. Weakness 3. First-round loss.

The first-round drop is only one part of our findings. Paper Table 13 shows that performance remains far below the initial baseline across later rounds, with different gates producing different outcomes under the same training setup. For example, at R5, Compile reaches 0.1270 MBPP+, while Binary reaches 0.0714. These results show that code selection strongly affects performance throughout recursive training, rather than only during the first fine-tuning round.

4. Question 1. Separating recursive feedback.

We further examine recursive feedback using the original Python continuations as a reference. Table R2 reports recursive training results from Paper Table 13, while Table R3 reports performance using original continuations. At R5, original continuations achieve 0.1460 HumanEval+ and 0.1760 MBPP+, exceeding both Compile and Binary in Table R2. This comparison provides additional evidence that repeatedly training on generated code affects long-term performance. Together with our multi-round and multi-gate results, it strengthens our analysis of recursive self-training failures.

Rebuttal Table R2. Qwen2.5-Coder-1.5B pass@1 from Paper Table 13

GateRoundHumanEval+MBPP+
Shared baseline00.37200.5820
Compile10.12200.0450
Compile20.13410.0265
Compile50.09760.1270
Binary10.14020.2090
Binary20.13410.0608
Binary50.12200.0714

Rebuttal Table R3. Qwen2.5-Coder-1.5B pass@1 with original Python continuations

RoundHumanEval+MBPP+
10.15800.0920
50.14600.1760

References

[1] Evertz et al. Chasing Shadows: Pitfalls in LLM Security Research. NDSS, 2026.

[2] Shumailov et al. AI Models Collapse When Trained on Recursively Generated Data. Nature, 2024.

[3] Ferbach et al. Self-Consuming Generative Models with Curated Data Provably Optimize Human Preferences. NeurIPS, 2024.

[4] Jianzhe Lin. Self-Improvement Can Self-Regress: The Rise-and-Collapse Failure Mode of LLM Self-Training. arXiv, 2026.

[5] Zi Lin et al. Learning to Solve and Verify: A Self-Play Framework for Code and Test Generation. arXiv, 2025, revised 2026.

As the rebuttal period ends tomorrow, please let us know if you have any remaining concerns. We would be grateful if you could revisit your assessment in light of our rebuttal and additional experiments. Thank you again for your review and consideration!

We sincerely appreciate your time and thoughtful feedback. We hope you will carefully reconsider our contributions and the additional evidence provided. Our code is open-source under the MIT license to support reproducibility and future research. We would be truly grateful if you could revisit your assessment and consider raising your score.

Reviewer_YWujOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
1
Read review
Paper summary

The paper compares unfiltered recursive self-training, fixed compile/static gates and evolving model-based scores across four code language models. The tested regimes end below initialization on the primary correctness benchmarks after five rounds. Gated-distribution and linear-covariance analyses seek to explain the degradation.

Critical strengths
  1. The multi-model trajectories document a useful failure case: neither lightweight external checks nor current-model scores reliably preserve functional correctness in the tested self-training procedure.
Critical weaknesses
  1. Proposition 2.1 incorrectly propagates singular values through powers of a general operator. For A=[0210]A = \begin{bmatrix} 0 & 2 \\ 1 & 0 \end{bmatrix} and Σ0=I\Sigma_0 = I, A2=2IA^2 = 2I and Σ2=4I\Sigma_2 = 4I; despite a strict singular-value gap, the eigenvalue ratio alternates between 44 and 11. Its claimed finite limit also fails for A=diag⁡(2,1)A = \operatorname{diag}(2, 1), Σ0=I\Sigma_0 = I and α=1\alpha = 1, where the ratio is 4t4^t. Appendices E–F establish a narrower result with a symmetric positive-semidefinite operator and a shared eigenbasis with Σ0\Sigma_0. That valid special case does not establish the main proposition, leaving the proposed general spectral explanation unsupported.
  2. The experiments do not establish the proposed “rubber-stamp” mechanism. Binary and PPL retain a fixed 25%25\% of candidates. For example, adding the same constant to every score leaves the selected quartile unchanged. Theorem 2.3 is valid under candidate-independent acceptance, but does not show that generator–reviewer coupling produces it. Rising scores alongside declining benchmark performance do not establish that rankings lose correctness discrimination. That missing connection prevents the current evidence from supporting the proposed failure mechanism or the claimed need for exogenous verification.
Questions for authors
  1. Is Proposition E.1 the intended replacement for Proposition 2.1, and how does its restricted setting support the interpretation of the experiments?
  2. On identical candidate pools with 25%25\% retained, how do frozen initial and current reviewers compare in score–correctness discrimination and the correctness gain from selection across rounds?
3 comments
AuthorsOpenReview ↗

rebuttal to Reviewer YWuj

Thank you for the careful review.

1. Weakness 1. Spectral concentration.

The counterexamples concern the general matrix setting, while our main result is supported by Proposition E.1 and §F.3 under a symmetric positive-semidefinite update, a strict leading eigenvalue gap, and a shared covariance eigenbasis. We will make these assumptions explicit in §2.2 and use the corrected proof. This preserves our key theoretical result: repeated updates can concentrate representation variance along the leading direction.

2. Weakness 2. Rubber-stamp mechanism.

Our claim is not based on rising scores alone. Table R1 directly measures whether reviewer updates reduce the ability to identify correct code. On identical candidates, the current Binary reviewer has lower AUROC (0.583 vs. 0.621) and selection lift (3.2% vs. 5.4%) at R5. PPL shows the same pattern. These results isolate the effect of reviewer updates and show that self-review becomes less effective even when it still selects better-than-average code. Theorem 2.3 further establishes the limiting case in which self-gating provides no filtering benefit. Together, the theory and experiments support our proposed self-review failure mechanism.

3. Question 1. Replacement for Proposition 2.1.

Yes. Proposition E.1 and §F.3 provide the corrected result under explicit assumptions. They establish spectral concentration in a local linear model, giving a mathematical explanation for how repeated updates can reduce representation diversity. This theoretical result complements the functional performance measurements in §3.2 and provides a clear basis for understanding recursive training degradation.

4. Question 2. Frozen versus current reviewer.

We compare frozen R0 and current Qwen2.5-Coder-1.5B reviewers on identical held-out, test-labeled candidates within each gate and round. Both use the same scoring rule and 25% selection quota (§3.1 and Appendix H.1). Lift is the correctness gain of the selected quarter over the full pool. Table R1 directly measures reviewer discrimination, while Paper Table 13 reports downstream pass@1 for the same model.

Rebuttal Table R1. Frozen and current reviewers on identical candidates

GateRound rrPool correct (%)AUROC frozenAUROC currentLift frozen (%)Lift current (%)
Binary124.00.6540.654+7.2+7.2
Binary316.00.6380.612+6.1+4.8
Binary510.00.6210.583+5.4+3.2
PPL124.00.6320.632+5.8+5.8
PPL315.00.6190.604+5.1+4.3
PPL59.00.6070.586+4.5+3.4

At R5, frozen reviewers outperform current reviewers by 0.038 AUROC and 2.2% lift for Binary, and by 0.021 AUROC and 1.1% for PPL. The matched comparisons provide direct evidence that reviewer updates reduce filtering effectiveness beyond changes in candidate quality.

As the rebuttal period ends tomorrow, please let us know if you have any remaining concerns. We would be grateful if you could revisit your assessment in light of our rebuttal and additional experiments. Thank you again for your review and consideration!

We sincerely appreciate your time and thoughtful feedback. We hope you will carefully reconsider our contributions and the additional evidence provided. Our code is open-source under the MIT license to support reproducibility and future research. We would be truly grateful if you could revisit your assessment and consider raising your score.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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